Cheng et al. discuss the community structure of functional climate networks based on correlations among daily near-surface air temperature variations around the globe. They report systematic changes in the statistical properties of the network communities since the early 1980s and attempt to uncover the backbone of those changes in terms of a changing abundance of “isolated nodes”. With its topical scope, the manuscript adds to a growing body of research utilizing network methods for studying the spatial organization of strong correlations in the global temperature field, as well as other climate variables at global and regional scales. The reported findings could be interesting, but are in my opinion not well enough explained, reflected regarding, and embedded into the context of existing knowledge on both climate variability and change and the methodological potentials and limitations of the employed type of network approach.

In more detail, I have the following remarks that the authors should take into consideration when revising their presented work:

Line 18: It appears physically implausible, at least questionable, to speak of “nodes [grid points] experiencing amplified insolation”. The insolation (i.e. amount of solar radiation directly reaching the Earth’s surface) has not changed markedly over the period under study (except for changes in solar activity and maybe different atmospheric absorption by different types of aerosols). What likely has gradually changed is the amount of backscattered radiation that is kept within the atmosphere due to changing concentration and distribution of greenhouse gases and thereby contributes to warming the planet.

Lines 21-22: It is not clear how the authors reach the conclusion that weakening ocean current interactions may be responsible for the observed findings. The presented manuscript does not study oceanic variables, but only near-surface atmospheric conditions, and hence allows at most for very indirect inference of possible links with changes in ocean circulation. Moreover, it is not clear what kind of “interactions” the authors may have in mind. (Do they mean tropical basin interactions via atmospheric pathways?)

Line 27: Ocean acidification and glacier melting are not extreme events and hence referred to here out of context.

Lines 31-41:  The authors cite here three recent, apparently randomly selected studies, the relationship of which with the topic and/or methodology of the present paper is not really clear to me. I would expect a more careful selection and discussion of relevant references at this prominent place of the Introduction.

Line 42: What do the authors mean by “diversity”? Diversity of what?

Lines 45-63: Similar as in the first paragraph of the Introduction, the selection of references on climate network analysis presented here appears not very systematic and concentrated on studies topically relevant to the presented work.

Line 48: The statement “variables such as temperature or geographical location are used as network nodes” is nonsense. Nodes in a climate network are identified with geographical locations at which temperature (or any other climate) time series are available for analyzing their bivariate similarity (e.g. correlation). In this regard, it is quite uncommon to use covariance instead of correlation (as suggested in line 49), since absence of normalization would lead to regions with high variance of temperature would then dominate the network connectivity.

Lines 73-79: The authors state that “there are many researches on the internal dynamics mechanisms of [the] climate system based on community structure”, but cite just two of them. The second part of this block of sentences, “some studies have identified novel dynamical mechanisms of climate systems through the characteristics of community structures in networks”, however cites a few studies, but all of them entirely out of context. Tsonis et al. (2007) is wrongly referenced to have appeared in Chaos (correct would have been Geophysical Research Letters) and just uses five climate indices, for which a consideration of network communities does not make any sense. Gozolchiani et al. (2008) is also falsely attributed to the journal Chaos instead of EPL and does not discuss climate network communities either. Swanson and Tsonis (2009) does not make use of any community or network concept, too. Finally, Elsner et al. (2009) uses visibility graphs, a concept entirely different from that used in the present work, without any referencing to community detection. Hence, I have to conclude that all four references to this sentence have nothing to do with the suggested statement.

For community detection in their near-surface temperature network, the authors use the Louvain algorithm; however, this choice is neither explained nor justified. I would like to draw the authors’ attention to Fig. 8 of Kittel et al. (Eur. Phys. J. ST, 2021). This figure compares the year-by-year variability of modularity for a (full-resolution) evolving climate network of surface air temperature anomalies (similar to that studied in the present work) obtained by different community detection algorithms, demonstrating that the choice of methodology may be crucial for the outcomes of community detection and may lack robustness.

Lines 94-96: The authors report that they “strategically select” 726 out of 10,512 grid points, but they do not describe how and why. With the information given in the Data section, the presented analysis is not reproducible. In fact, the heterogeneity or homogeneity of the spatial density of the considered nodes has a crucial effect on any network properties in climate networks, since nearby nodes are likely to have larger statistical similarity of climate variability (and, hence, a higher likelihood of being connected in the network). Possible solutions include consideration of area-weighted network measures (Heitzig et al., Eur. Phys. J. B, 2012) or specific selections of nodes when subsampling original fixed latitude-longitude grids in climate records (Radebach et al., Phys. Rev. E, 2013). I am afraid that without such consideration (that I do not see reported in the paper), the inter-node distance in high latitudes is much smaller than close to the equator, and accordingly the spatial placement of network connectivity is heavily biased towards the polar regions. Under such circumstances, it would be highly questionable to what extent the reported findings of the present work can actually be interpreted meaningfully.

Line 101: Detrending and subtracting the average seasonal cycle are two entirely different things.

Line 108: Why do the authors use a maximum lag of 200 days for an analysis of time windows of just 365 days? How robust are the reported results regarding this choice?

Line 111: Why do the authors list “minimum value” here when it is not made use of? What are maximum, (minimum,) mean and standard deviation taken from? In Equation (3), left and right-hand side have the same indices, so this description is mathematically inconsistent. Also the following text is quite problematic. It is correct that strong auto-correlation inflates the significance of the cross-correlation, but not the cross-correlation itself. It is not clear how the link strength can eliminate the effect of serial dependence. For the latter purpose, a better alternative might be the consideration of p-values, as originally suggested by Palus et al. (Nonlin. Proc. Geophys., 2011), which however have considered only lag-zero correlations.

Lines 120-122: Does the outcome of the Louvain algorithm depend on the order with which the different nodes are considered in the algorithm? I would also recommend some brief discussion on the convergence of the method to some global modularity optimum (respectively, the risk to approach some local optimum by following this iterative methodology).

Line 127: k_i and k_j are the degrees of the nodes i and j - not the sums of the link weights (which would be the node strengths). The formula for modularity given in Eq. (4) applies to unweighted networks.

The authors choose their running time windows to coincide with the calendar years. This may bear the risk of mixing months affected by a declining El Nino (winter/spring) with those of an approaching La Nina (fall/winter) – or vice versa - during the same year. From numerous previous works, we know that El Nino and La Nina prominently affect global surface air temperature anomaly based networks (see works by Gozolchiani et al. (2008), Yamasaki et al. (Phys. Rev. Lett., 2008), Tsonis et al. (Phys. Rev. Lett., 2008), Ludescher et al. (PNAS, 2013), Radebach et al. (Phys. Rev. E, 2013), and many others). Mixing the effects of opposite ENSO phases might blur the analysis results (especially since the statistics of El Nino and La Nina episodes has changed over the last decades). I would suggest repeating the presented analysis with time windows shifted by 6 months to check for the robustness of the reported findings.

Lines 142-143: It is trivial that average community size and number of communities display opposite trends, since both characteristics exhibit a trivial inverse proportionality: <s>=N/N_c. So discussing both characteristics appears somewhat pointless to me.

The authors attribute the timing of the identified changes in community statistics around the year 1982 to the 1982/83 El Nino episode. I am wondering if there are any other findings demonstrating a similarly long-lasting effect of this particular El Nino event on the global climate system. Besides overall global temperature rise (being heterogeneously distributed in space and time), other potential reasons for the reported marked shift in community properties have not been discussed (including multidecadal variability). Tsonis et al. (2007) and Swanson and Tsonis (2009) – two references cited in the present manuscript – have partly discussed a late-1970s climate shift, and could serve as an initial source of inspiration for identifying further potential origins (but there is far more, also more recent, literature). In terms of the used dataset, one should also not forget that the availability of satellite data assimilated into the reanalysis products has started only in the late 1970s, so that the observed changes could also be affected by underlying heterogeneities in the considered data. I do not claim that this is the case, but this possibility cannot be simply ruled out by the present analysis.

Figure 1f: Since the community sizes have been binned for showing the relative frequencies (likely a more suitable term than “probability”), I would recommend showing them as a histogram with bars instead of a line plot. Alternatively, a cumulative distribution plot taking all explicit values of community sizes into account might be a reasonable alternative.

Line 158: Nodes are commonly called isolated when their degree is zero (i.e., there do not exist any links to other nodes). It is not clear if the definition of community size 1 considered here is equivalent, or if nodes can also form a community of size 1 under the Louvain algorithm if there exist such connections (and if so, why such nodes are not attributed to any community). This should be clarified. In any case, I would recommend using the more standard definition of degree k_i=0 for isolated nodes to avoid confusion. Note that the fact that “isolated nodes” are commonly restricted to the tropical belt (Fig. 2, ll. 181-184) is compatible with my aforementioned concern regarding a connectivity bias towards the poles due to the heterogeneous spatial density of nodes.

A non-mandatory suggestion: The authors study the number of communities (which, when viewed from a statistical perspective as a clustering problem, is a matter of statistical model selection that is not clearly described in the manuscript) – along with the equivalent information on average community size – along with the corresponding modularity. In network theory, there is the more fundamental concept of components (if the network is split into disconnected subgraphs), which are less ambiguous than communities. (Besides both depending on the threshold for distinguishing links from non-links.) I wonder if statistics used in the analysis based on network components could be adapted to communities as well (e.g., the size of the largest group of nodes, the number of groups with two elements, or others, which are often considered for network components in the study of percolation processes). Maybe such measures might provide any useful additional information beyond the two characteristics studied in the present manuscript.

Lines 186-188: Attributing the changes in community structure (especially increasing frequency of isolated nodes) to global warming (i.e., the average temperature at all considered nodes) could be merely a coincidence; a direct statistical link between these properties (which all change gradually with time) has not been demonstrated nor discussed in a plausible manner. Especially, lines 217-219 suggest increase ice melt as one reason for the reorganization of network connectivity, which however hardly explains the changes reported by the authors, which are most dominant in the tropics where there is hardly any ice to melt. Lines 221-224 appear as an attempt to put the reported findings into a broader context, but any details are unfortunately missing. What are specific processes, and could the authors support their corresponding claims by appropriate references?

The manuscript provides a comprehensive analysis of the climate system's evolution under the impact of global warming, employing climate network methods. The authors have effectively used climate network analysis and Louvain community detection to reveal a significant phenomenon: notable alterations in the climate network's structure. These changes include the network's modularization, the number of communities, and the average size of these communities. A particularly striking finding was the shift in the community structure around 1982, marked by a significant rise in isolated nodes, predominantly in the equatorial ocean regions.

The study is engaging and well-articulated. Nonetheless, I have a few reservations that I believe, if addressed, could further solidify the scientific validity of this manuscript:

The field of complex network studies presents a variety of community detection algorithms, among which Louvain is a prominent choice. It would enhance the manuscript if the authors could elucidate their preference for the Louvain algorithm over other available options. Alternatively, to affirm the robustness of their findings, the authors might consider applying and comparing results from different algorithms.

There is a grammar error in line 32; it should be "researched" instead of "research."

Lines 35-36: Previous papers have reported the collapse of AMOC; please provide more relevant references.

In lines 42-43, the statement "The climate system is highly complex, characterized by diversity, multiscale dynamics, and nonlinearity" is vague and should be clarified.

In line 47, change to "(e.g., precipitation, temperature, and wind)."

Line 49: The link of the climate network can be defined in various ways, such as synchronization and mutual information.

In line 52, use past tense in "Donges et al. employed..." and ensure consistency with tenses in surrounding sentences.

Line 70: Remove "deeper."

Line 95: Clarify why 726 nodes were chosen in detail.

Line 108: Add the unit of the time lag.

Lines 112-114: The statement “The strength W_{ij} reflects the deviation and serves to eliminate the effect of autocorrelation, aiming for a more desirable outcome.” needs additional support or citation of a relevant study.

Lines 221-224: The conclusion mentions enhanced connectivity between nodes in the equatorial region and the European continent due to changes in atmospheric circulation patterns. Consider citing relevant literature to support this claim.